In this paper, the authors apply a theoretical framework they developed in previous work to evaluate the sensitivity of tropical orographic precipitation to changes in background wind speed. The theory predicts that precipitation increases with increasing wind speed by 20-30% per m/s, and find good agreement with this prediction in a numerical simulation using the Weather Research and Forecasting (WRF) model. They also find qualitative agreement with their prediction in observations.

The paper is well written. The result that tropical orographic precipitation doesn’t scale in proportion to the horizontal wind speed is interesting and has important implications for climate change impacts given possible future changes in the tropical circulation. The agreement between theory, models, and observations is imperfect but mostly convincing.

The main room for improvement, in my view, relates not to the analysis per se but to the way it’s explained. I like the authors’ approach of combining linear mountain-wave theory with a convective closure to study orographic enhancement of precipitation over tropical mountain ranges like the Western Ghats. However, aside from the two previous studies published by the same authors, this is a novel approach, and one that I suspect many readers will not be very familiar with. I think the authors should do more to explain the physical basis for their approach, including, for example, why they assume a dry static stability for the linear mountain wave solution, and why the convective closure of Ahmed (2022) makes sense in this context. I also think the authors could hold the reader’s hand a bit more on some of the more technical parts of the paper, especially when using their equations to draw physical conclusions. I note some specific areas of confusion for me below.

Sections 2 and 3: I may have missed it, but I couldn’t find any mention of the vertical humidity profile in either the theory or numerical modeling. Isn’t that important given that the lower tropospheric humidity perturbation is based on the vertical humidity gradient (Eq. 2)?

Line 93 and Fig. 1A: I understand why the depth of ascent would increase from a change in the vertical mountain wavelength, but I’m surprised there’s not an increase in the *magnitude* of eta (and thus T’) from an increase in U, given the lower boundary condition w=u*dh/dx (Fig. 1b). Later the authors note that the ratio of w/U increases in response to an increase in U, which I would expect to further amplify the T perturbation. What am I missing?

Section 3.3: I found this discussion of the role of theta_e’ to be confusing. The basic argument, as far as I can tell, is that there’s a theta_e perturbation that contributes to precipitation enhancement, and that this is tied to the greater vertical penetration of the mountain wave when U increases, since an increase in the vertical wavelength causes w/U to increase above the surface, and this in turn increases the vertical advection of theta_e. First, I didn’t find the evidence in Fig. 3c to be especially convincing given the large magnitude of the residual term. Also, shouldn’t the same increase in vertical advection also apply to T and q? In reality, the WRF simulations show no contribution from q' and a relatively modest contribution from T'. I think this disagreement between the theory and WRF simulations should receive more attention.

In summary, I think this is an important contribution, but I wish it provided a clearer physical explanation for why tropical orographic precipitation is so sensitive to perturbations in U. The simple theory that involves q and T seems relatively straightforward (aside from assumptions about the vertical profile of q). However, while this theory gives an accurate prediction for the precipitation increase simulated by WRF, it seems to do so for the wrong reasons, since WRF shows a negligible contribution from q’ and a large contribution from theta_e' (Fig. 2c). I think the authors should better explain how their theory can be reconciled with the WRF results.

Summary: in this manuscript, the authors apply their new theory of mechanically forced orographic convection (Nicolas and Boos 2022) to evaluate the sensitivity of orographic precipitation to background wind speed. The theory is augmented by convection-permitting WRF simulations and observations from selected mountainous tropical regions. In the end, the authors conclude that small increases in winds in current and future climates may give rise to disproportionate increases in orographic precipitation.

I found the manuscript to be mostly well written and scientifically rigorous. The figures are clear but also very densely packed with information, and the authors dutifully explain each detail in their very long figure captions. In terms of the methodology, the theoretical model is already vetted and on solid footing and the complementary simulations and observational analyses add substantial value. The results are scientifically interesting and mostly convincing. Overall, this is a strong manuscript, and my feedback consists of one major comment along with a number of minor and/or technical comments.

Major comment

1. The physical explanation for the enhanced \theta_e over the windward slope in the U=12 m/s case in Figs. 3A-B is not convincing to me. The authors attribute this enhancement to increased vertical advection of \theta_e in Fig. 3C. They argue that this increase must be associated with a deeper mountain wave, which is evident at upper levels (well, above 800 hPa) in Fig. 1B. However, the clear enhancement in \theta_e in Fig. 3A is confined to the 900-1000 hPa layer, not above 800 hPa. Moreover, some of this enhancement reaches all the way down to the surface in Fig. 3A, where the authors concede that the mountain wave cannot explain the enhancement. I’m skeptical of this interpretation because, although vertical advection is stronger at larger U, so is horizontal advection, which tends to reduce \theta_e. Also, if the air crosses the mountain in both cases (which it does), and \theta_e is in fact conserved, the \theta_e over the mountain top should be the same in both cases even though the terms in the \theta_e budget may differ in magnitude. Therefore, my sense is that more analysis is needed to properly interpret this enhancement, which is important because it is largely responsible for the disproportionate increase in P’ with U. One possibility is that relative flow deceleration caused by the mountain wave over the windward slope (relative to the background wind speed U) may be smaller in the U=12 m/s case. If so, the near-surface W would be disproportionately enhanced. Also, because this is an orographic precipitation problem, one can never rule out cloud microphysics as a driver of changes. Is it possible that the U=12 m/s case sees a larger share of the precipitation evaporating over the lee slope, as opposed to over the windward slope? Weak evidence of this is seen in the slight downstream shift of the precipitation peak for the U=12 m/s simulation in Figs. 3A-B. Such a change could reduce evaporative cooling over the windward slope, thereby enhancing boundary-layer \theta_e there.

Minor comments:

1. Abstract, L5-6: this sentence is confusing and misleading. First, it is said that precipitation is “enhanced”, but the term “enhancement” requires a reference state for comparison. What is that reference state? This context is necessary in the current study, where the term “enhancement” could refer to (i) orographic enhancement relative to surrounding regions, (ii) enhancement relative to cases with weaker or stronger winds, or (iii) enhancement relative to the current climate. Moreover, the description of the model seems off the mark. It’s a model for orographic precipitation, right? So why not describe it as such?
2. L29 and L35-36: I agree that decades of research have facilitated progress in orographic “rainfall” (or “precipitation”). But here the authors only refer to studies of tropical orographic precipitation, and only a very small sampling of those. My concern is that the authors preemptively limit the scope of their literature review to a narrow topic. Doing so helps to shorten the discussion, but it also precludes the authors from benefiting from a huge tranche of relevant literature. There are numerous studies of midlatitude orographic precipitation, ranging from theoretical, to numerical, to observational, many with ideas that clearly transfer to the current study. For example, using idealized simulations, Colle (JAS, 2004) found 20 years ago that stronger winds enhance orographic precipitation by deepening the mountain wave. His result seems quite relevant to the present study. Of course, the goal is not to cite as many studies as possible, but to use the existing literature to help frame and inform the scientific investigation.
3. L72: By “adiabatic”, do you mean dry or moist adiabatic?
4. L85-86: “Thus, we expect Pm << Pa”: Where does this inference come from? It is not clear from eqn (3) nor the text of this sentence.
5. L27: More information on these simulations would be helpful. Do they ever reach a quasi-steady state? How long does it take? If 250 days are required (as the text suggests), that would seem rather excessive.
6. L132-133: Here the authors do cite a midlatitude orographic precipitation study but the physical reasoning is flawed. Yes, hydrometeor drift is significant, but Smith and Barstad (JAS, 2004) were exclusively interested in stratiform precipitation. They were assuming that part of the cause for the downstream shift was slow falling (~1 m/s) ice and snow being carried downwind. This effect is  weaker for the convective precipitation studied here, where fall speeds are closer to 10 m/s. Therefore, I think the "10 km" estimate is overly generous.
7. L134: Does the theory even consider multiple levels? This isn't apparent in equation (1) or the Appendix. Anyway, shouldn't the precipitation amount scale with low-level specific humidity? If not, the theory would have little hope of capturing the sensitivity of orographic precipitation with respect to temperature variations in a changing climate.
8. L158: What is meant by “equally”? The two contributions don’t seem precisely equal to me, so this is misleading.
9. L160-161: I don't follow this reasoning. You just said that qL' has minimal impact but θ_e does, so how can one compensate for the other? And why is there an “absence of free-tropospheric moistening”? Doesn't the mountain wave ascent produce this moistening?
10. Equation (4): I don’t think it’s fair to claim that the \theta_e budget is equal to the highly simplified (4) without stating which simplifying assumptions were made.
11. L174: “Little accuracy is lost…”: is this shown somewhere? Given my major comment, I would be interested to see the evidence behind this statement.
12. L175 and L141: Why do you average 4000-2000 km upstream of the mountain here but over a different region (4000-2500 km upstream) on L141? Is there a justification for this inconsistency?
13. L183: I’m not so sure that a \theta_e change on the order of 0.1 K in can be called a “sharp” increase.
14. L206-207: Do all reanalyses used in this paper really use a “model prior to 1979”? I thought ERA5 used a modern numerical model. Or maybe I am not reading this sentence correctly.
15. L225: Measured how? Using gauges, as you claimed earlier? Surely the gauges don't align perfectly with the line shown in Fig. 4B. What data set are you using, and how are you analyzing these data? In this section you use a variety of data sets, and the reader needs some help to keep track as you weave through different analyses.
16. L229-230: OK, but what about P'? Are you saying here that P’ should be a function of P0? That's not what was assumed in the linear model.
17. L259-260: “assuming a 3.5 K warming”: measured where? At the surface???
18. L263-269: Related to this text, another midlatitude study is Kirshbaum and Smith (QJ, 2008), who found < CC scaling w.r.t. temperature changes in simulations designed to test this exact question. Their result and physical explanation is very similar to the one posed by O'Gorman and Schneider (2009) for the climate at large, but with a slightly different mathematical formulation.
19. L288-291: Another limitation that should be acknowledged is the fact that orographic convection is poorly resolved at Δ= 3 km (Kirshbaum, JAS 2020). The model effective resolution is no better than 20 km, and orographic cells typically have horizontal scales of 1-10 km. Also, for larger temperature deviations one must also consider cloud-microphysical changes (e.g., less ice-phase microphysics) that could offset the projected enhancements in regions experiencing significant warming.